acceptodds
Withdrawn from ICLR 2027

Validating Discovered Differences in Model Replacement Audits

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

When an AI model is updated or replaced, we need to know how its behavior changes. Testing every possible input is impractical, so we search for behavioral differences between the original model and its replacement. But search creates two problems: a discovered difference may not hold on other inputs, while a search that finds no difference may still miss differences elsewhere. We separate what search discovers from what the evidence supports. Before search, we specify how discovered differences will be followed up on new inputs, and fresh validation determines whether there is enough evidence to support them. A false acceptance occurs when validation supports a difference that does not actually hold. Our validation controls this rate across search strategies. On Berkeley Function Calling Leaderboard (BFCL) tasks and controlled experiments, it validates differences on new inputs without false acceptances, while a simpler baseline produces a 49.44% false-acceptance rate. When search finds no difference, we instead analyze coverage of the untested inputs. Using a bound on how much the difference can change between nearby inputs, we determine when tested inputs can rule out differences elsewhere. Experiments show that limited coverage can leave existing differences undetected. Together, validation and coverage clarify what can and cannot be concluded about behavioral differences without exhaustive testing.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
model replacement, model evaluation, adaptive search, post-selection validation, statistical validity, coverage analysis

Reviews

Among:
Shape:
1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_DHSfOpenReview ↗
Rating
1
Confidence
2
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

This paper aims to address two important auditing problems theoretically and empirically: 'First, a difference found during search may not hold on a broader population of inputs, especially because search favors large observed differences. Second, a search that finds no difference may still miss differences on inputs that were not tested.' The important experiments E1, E2 and E3 are used to support their theory/framework, and they cover 'search-selected differences through fresh validation', 'the validation rule under controlled population truth', and 'negative search outcomes'.

Critical strengths

This paper focuses on the model replacement auditing problem, which is a relevant research challenge. The authors address this problem theoretically and also test their framework on a function-calling benchmark BFCL and in controlled simulations. The theoretical proofs (Theorem 1, Props 1 and 2) appear sound. I used Claude Fable 5.1 to help me check them and found no errors.

Critical weaknesses
  1. The research challenge is not well presented. It lacks a clear problem statement section in Sec. 2, and many invented terms in this specific research case, such as 'contracts' and 'kernels', are only briefly defined, and after their first use. Also, no related work section is given to help the readers dive into this topic. This is consequential because, without that positioning, it is hard to see what is new: the validation procedure is a standard holdout with a Hoeffding bound.

  2. The practical usage of the proposed theory/framework is not well addressed. The three experiments E1-3 are proposed to support the two studied research questions, but do not highlight their real usage in applications. Replacement in E1 is a convex combination of peer-model scores rather than an actual candidate model, and the negative-search result requires a Lipschitz constant that the paper admits does not hold on its real data.

Given the two points above, it is hard to estimate how much impact or effectiveness this framework could have for future research in auditing.

Questions for authors
  1. Is there any related work that connects to the invented vocabulary in this work (e.g., contract, regime, kernel)?

  2. What do the legends in Figure 1 mean? The axes and markers are only defined in Section 3.

  3. E1-3 are mentioned in the introduction without giving any details, so it does not help to understand the paper. Together with question 2, the main motivation needs to be presented in a better way.

  4. Why is the replacement in E1 a convex combination of peer-model scores rather than an actual candidate model?

  5. The negative-search result needs a Lipschitz constant L, which the paper admits does not hold on the real data. How can L be estimated in practice?

Reviewer_SVPWOpenReview ↗
Rating
1
Confidence
2
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

I found this paper really hard to understand and was not able to assess its methodology or evaluation. However, I believe that this does not actually come from missing background knowledge on my part, but mostly from the way the paper introduce and formalizes the problem. Therefore, I am going to take some rather unorthodox way of reviewing the paper by trying to show how I approached the paper: Fundamentally, the paper is akin to a regression test setup: When a model is deployed we can verify certain properties (e.g., that it behaves correctly on some set of inputs and similar, derived inputs). However, when the model changes, the former correct samples (and families of samples) might suddenly lead to unexpected, wrong behavior. While we could enumerate a test dataset, this would always miss data that is close to the tested data and might now be misclassified. The paper's problems start with the notation which, to my knowledge, is non-standard as I could not find this notation in references papers (Perez et al. 2022; Patil et al. 2025; Ajjara & Basu, 2026). While this in general is no problem, the convoluted notation makes it more difficult to assess. The notations starts with the original model ftf_t, which has the undefined subscript tt, and a candidate replacement sCs_C, which has the undefined subscript CC. I assume that both of these are just regular inference model, e.g., ft(x)f_t(x) and sC(x)s_C(x) for some input xx. Then some "action" aa is defined which sends a controlled case to both systems. I assume that an action a1a_1 means that the models receive for example ft(x1)f_t(x_1) and sC(x1)s_C(x_1) while an action a2a_2 receives ft(x2)f_t(x_2) and sC(x2)s_C(x_2), where x1x_1 and x2x_2 are some inputs. Then a "world" WW and "response laws" YtW(a)Y_t^W(a) and YCW(a)Y_C^W(a) are defined, both of which are unclear to me. Are these / do these return scalars, vectors, probability distributions? Next, the notation for the "predeclared feasiblity rule" FW(a)=ϕF(a)∈{0,1}F^W(a) = \phi_F(a) \in \{0,1\} is declared, which is completely unclear to me. What is FF? Why is it equal to ϕ\phi? Why do we need that apparent redundancy? What do these function assess in the actions? The paper then goes on to define, what appears to be a loss ZCW(a)=l(a,YtW(a),YCW(a))∈[0,M]Z_C^W(a)=l(a, Y_t^W(a), Y_C^W(a)) \in [0, M], but again does not clarify what this loss is or why it is limited by MM (or even what the interpretation of MM is). The next section, further introduce unclear notation (a regime z∈Zz \in Z, u∈Uzu \in U_z, a(z,u)a(z,u), KzK_z, ...). In my opinion, the authors should significantly rework their terminology and notation using established notation, e.g., starting with f(x)f(x) for inference on a model; or f1(x)f_1(x) and f2(x)f_2(x) for the evolution of a model, then defining a loss for the model performance and/or for the auditing system. Given the apparent association to differential privacy (with regards to finding if/how models differs) that terminology and notation could be borrowed alternatively. In any case, the framework needs to be made more accessible for a reader and the reason for additonal notation needs to be well formulated. If this is established notation I am just not familiar with, the paper would benefit from citing related work where this notation is borrowed from. Reading on, I was ultimately overwhelmed by the poorly motivated terminology and notation. In the current state of the paper, I am not able to validate either the methodlogy or evaluation. I therefore suggest rejecting the paper.

Critical strengths
  • Good motivation
Critical weaknesses
  • Severe presentation issues regarding notation and terminology
Questions for authors
Reviewer_PPzkOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper addresses the problem of when an a model is replaced by distillation, routing, or switching we would want to understand the differences in the model behavior beyond just aggregate performance. Techniques like adaptive search can find inputs where behavior differs but the differences may not generalize to the broader population. The authors propose a counterfactual witness interface that separates search from validation. A pre-specified audit contract freezes the systems, regimes, and population kernels before search, then, after search a regime is selected and fresh cases from that regime's declared population are used for validation. The paper provides a formal guarantee that false acceptance is controlled uniformly over all adaptive discovery policies. They evaluate the approach on Berkeley Function Calling Leaderboard tasks, controlled calibration worlds, and negative-search coverage.

Critical strengths

The core contribution is genuine and the paper formalizes a real gap that practitioners face.

The search-vs-validation split is the right abstraction. The paper makes a compelling case that a discovered difference is not the same as population evidence, and the 65.3% non-witness rate among positive search findings (E1) is a striking demonstration of selection inflation.

I appreciate theorem 1 as the bounded discrepancy, i.i.d. fresh draws conditional on the discovery record, and independent response randomness are a good contribution. The proof via Hoeffding + union bound is simple and clear.

The authors point out that absence of evidence requires a coverage argument, and the Lipschitz-based fill-distance analysis (Proposition 1) gives a concrete, falsifiable criterion. The OFAT vs. full-factorial comparison (Table 3, Figure 7a) shows that query placement matters more than query count.

Hash-based provenance for contracts and reruns is a nice addition.

Critical weaknesses

I have a few concerns that the authors could address.

The regime family is fixed before search, but the paper does not discuss how to choose it. The entire method relies on the pre-declared regime family Z and kernels Kz. If Z is too narrow, real differences are missed (E3 shows this). If Z is too broad, the per-regime sample sizes shrink. The paper treats this as exogenous, but in practice, choosing Z is the hardest part of any audit. Some guidance (even a heuristic) would strengthen the practical contribution.

Only one claim is tested per audit. The verifier tests TC, ẑ for one selected regime. The paper explicitly notes that rejecting an entire replacement class requires a minimax record, but this stronger task is not evaluated experimentally. For a practitioner deciding whether to deploy a replacement, a single-regime witness is often insufficient. How does the framework compose across multiple selected regimes? A Bonferroni or sequential testing extension seems natural and is absent.

The BFCL instantiation is narrow. E1 uses function-calling tasks with a specific convex-combination replacement. The regime factors (return format, documentation format, tool-call tags) are surface-level formatting variations. It is unclear whether the framework would exhibit the same search-validation gap on semantically richer regime definitions (e.g., task difficulty, domain, input length). The paper should discuss how the nature of the regime space affects the informativeness of the audit.

The coverage analysis assumes L = 0.15 in a controlled 24-point space. The paper acknowledges that this assumption "does not hold for all neighboring regimes in the natural data." This undercuts the practical applicability of the negative-search result.

Questions for authors

How sensitive is the framework to misspecification of the kernel Kz? If the declared population does not match the true deployment distribution, what degrades first, false acceptance control or power?

Could you provide empirical estimates of the Lipschitz constant L from the E1 data, even as a rough bound?

Have you considered a sequential version where multiple regimes can be tested with spending-function control (e.g., alpha-spending)?

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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